A Study of Two Doses of Dulaglutide (LY2189265) in Japanese Patients With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Two Doses of Dulaglutide (LY2189265) in Japanese Patients With Type 2 Diabetes (NCT04809220), a randomized phase 3 study. The primary outcome is Change From Baseline in Hemoglobin A1c (HbA1c) at Week 26.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-arm study sponsored by Eli Lilly and Company. The registry record lists enrollment of 591 and status as completed. The study evaluated dulaglutide 1.5 mg and 0.75 mg in Japanese participants with type 2 diabetes, either as monotherapy or in combination with one oral antihyperglycemic medication.

Both groups received weekly subcutaneous injections during a 52-week treatment period. The arm descriptions distinguish participants using DPP-4 inhibitors: those medications were discontinued at randomization and the participants were regarded as receiving dulaglutide monotherapy. Other oral antihyperglycemic medications continued at the same dose. The registry record describes the study as approximately 58 weeks in duration.

The design was double-blind, meaning that the study was intended to keep treatment assignment masked, and parallel-arm, meaning participants were assigned to one of the two dose groups rather than crossing between treatments. Randomization is intended to support a fair comparison by distributing participant characteristics between groups on average, although it does not guarantee that every characteristic will be balanced.

The registry record lists study start as 2021-04-13 and primary completion as 2022-10-01. The original protocol’s sample-size justification, planned interim analyses, and detailed statistical plan are not reported in the registry record. The record does not establish from these registry entries whether the posted enrollment was the original planned number or whether any changes to enrollment targets occurred.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomly assigned participants, excluding the GCP compliance investigative site, who were exposed to at least 1 dose of study intervention and had at least one post baseline value for this analysis.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All randomly assigned participants, excluding the GCP compliance investigative site, who were exposed to at least 1 dose of study intervention.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Hemoglobin A1c (HbA1c) at Week 26, measured over Baseline, Week 26.

The primary endpoint was change from baseline in hemoglobin A1c (HbA1c) at Week 26, expressed as percentage of HbA1c. HbA1c is the glycosylated fraction of hemoglobin A. The registry record explains that it is measured to identify average plasma glucose concentration over prolonged periods. A change-from-baseline endpoint compares a participant’s measured value at follow-up with that participant’s starting value, and the group estimates summarize those changes.

The endpoint is continuous: it can take a range of values rather than representing only a category such as whether a target was reached. The reported least-squares means are model-based group estimates, not simply raw averages. The registry record says they were estimated using a mixed model for repeated measures, with baseline HbA1c, pre-study oral antihyperglycemic medication group, treatment, time, and the treatment-by-time interaction included as variables.

Week 26 was the primary time point; Week 52 HbA1c change was a secondary outcome. A difference between dose groups in mean change describes the comparative pattern in this analyzed population and at this follow-up time. It does not, on its own, establish what would happen for every participant or beyond the study period.

7. Results Posted in the Registry

• Dulaglutide 0.75 mg: mean -1.25 versus -1.53 on control; difference 0.28 (95% CI 0.14 to 0.42), standardized effect d = 0.33; z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline in HbA1c at Week 52

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Dulaglutide 0.75 mg: mean -1.19 versus -1.50 on control; difference 0.31 (95% CI 0.15 to 0.47), standardized effect d = 0.34; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Dulaglutide 0.75 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Fasting Serum Glucose (FSG)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Dulaglutide 0.75 mg: mean -33.10 versus -42.40 on control; difference 9.30 (95% CI 4.29 to 14.31), standardized effect d = 0.32; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Dulaglutide 0.75 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Body Weight

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Dulaglutide 0.75 mg: mean -0.20 versus -0.50 on control; difference 0.30 (95% CI -0.16 to 0.76), standardized effect d = 0.11; z-test p = 0.204.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dulaglutide 0.75 mg and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes extend the comparison beyond the primary Week 26 HbA1c endpoint. They include HbA1c change at Week 52, fasting serum glucose, six-point self-monitored blood glucose, body weight, and proportions reaching HbA1c targets. The registry record lists six outcome measures and reports five secondary outcomes in the posted results; it does not provide results for every listed secondary outcome in the registry record for this analysis.

Across the reported continuous secondary outcomes, the model-based estimates generally follow the primary result’s direction for measures of glycemia: the 1.5 mg group has the larger reported reduction in HbA1c at Week 52 and fasting serum glucose. The body-weight contrast is less precise, and its sponsor-reported p-value is 0.213. These outcomes broaden the descriptive picture but are not substitutes for the primary Week 26 comparison.

General: multiple outcomes create multiple opportunities to observe a small p-value by chance, even when no underlying differences exist. Methods such as adjusting significance thresholds or controlling an error rate can address this issue, but the registry record does not report whether such a multiplicity strategy was planned or used. Consequently, unadjusted secondary p-values carry less weight than the primary analysis, particularly when several endpoints and comparisons are considered together. The registry record also does not provide results for the listed six-point self-monitored glucose outcome or target-attainment outcomes in the registry record, so no inference about those findings can be made.

The secondary results are most useful as supporting context, with attention to their estimates and uncertainty rather than a simple count of statistically significant results. Their interpretation remains limited by the absence of a reported multiplicity plan and by the fact that the secondary outcomes address different measurements and follow-up times.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Change From Baseline in HbA1c at Week 52
• Percentage of Participants Achieving HbA1c Target ≤6.5% and <7.0%
• Change From Baseline in Fasting Serum Glucose (FSG)
• Change From Baseline in 6-point Self-Monitored Blood Glucose (SMBG)
• Change From Baseline in Body Weight

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mixed model estimate?

The primary result is reported as a least-squares mean (LS mean) change. General: a least-squares mean is an adjusted estimate from a statistical model. It can account for variables included in that model, rather than being only the unadjusted arithmetic mean of observed values. The registry record states that the primary model included baseline, pre-study oral antihyperglycemic medication group, treatment, time, and treatment multiplied by time. The record does not give further details about the model’s covariance structure or other implementation choices.

The endpoint was measured at baseline and Week 26, and the model is described as mixed model repeated measures (MMRM). General: repeated-measures models are used when outcomes are collected from the same participants at multiple time points. They can represent the relationship among measurements from one person and estimate treatment patterns over time. Their results depend on model assumptions and on how available observations are incorporated. The registry record does not report a full account of those assumptions.

What is the contrast?

The sponsor reports an LS mean difference of -0.29 with a 95% confidence interval from -0.43 to -0.14. In that reported comparison, the direction corresponds to the ordering of the two dose groups used by the sponsor. The simple unadjusted recalculation is stated in the opposite order, as 0.75 mg minus 1.5 mg, and is 0.28. Reversing the group order reverses the sign of a difference; it does not change the underlying contrast. Small differences in reported magnitude and interval can also reflect the distinction between the sponsor’s model-based estimate and a simple calculation from posted summary statistics.

What does the p-value say?

General: a p-value describes how incompatible data are with a specified null model, assuming that model and the analysis assumptions hold. It is not the probability that the null hypothesis is true, nor is it a direct measure of effect size or clinical importance. The sponsor’s primary p-value is <.001. The unadjusted recalculation reports p <0.001. These are strong statistical evidence against a zero contrast under the respective analyses, but the numerical result should be interpreted with the estimate and its interval, not alone.

Why show an unadjusted recalculation?

The recalculation uses posted group means, standard errors, and sample sizes to form a simple comparison. The pooled standard deviation is described as approximate because it is derived from the summary information. General: this kind of calculation can help readers understand the scale and precision of a contrast, but it does not reproduce a model that adjusts for baseline values, treatment history, and repeated measurements. It also should not be mistaken for an independently verified reanalysis of participant-level data. The sponsor’s reported mixed-model result is the analysis conducted for the registry record.

The calculated planning illustrations use an observed effect as their starting point and state assumptions of a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is a stated fraction of the observed effect. General: smaller target effects are harder to distinguish from random variation and therefore require more participants under the same planning assumptions. These are illustrative planning calculations, not a reconstruction of the original protocol’s design. The original design assumptions are not reported in the registry record.

How should the analysis population be understood?

The primary analysis included randomly assigned participants, excluded the GCP compliance investigative site, and required at least one dose of study intervention and at least one post-baseline value for the analysis. This is the registry’s stated population definition. It is not identical to a simple description of everyone randomized, because exposure and post-baseline measurement were eligibility conditions for this analysis. The record does not report a detailed accounting of participants excluded from each analysis or a full analysis-population flow.

General: restricting an analysis to people with observed follow-up can affect the interpretation if the availability of measurements is related to outcomes or treatment. Repeated-measures models can use observed measurements without requiring every participant to have every scheduled measurement, but valid interpretation depends on assumptions about missingness and the model. The registry record does not report the missing-data assumptions, sensitivity analyses, or imputation procedures, so those details cannot be evaluated from the posted information.

What is not established by the analysis?

The reported statistical comparison concerns average change at a specified follow-up in the defined analysis population. It does not establish an individual participant’s likely response, nor does statistical evidence alone establish clinical importance. The record does not report a clinically important difference threshold, multiplicity strategy, interim-analysis plan, or original sample-size justification. Those omissions limit how completely the reported p-values and planning illustrations can be connected to the study’s original analysis plan.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is an LS mean difference of -0.29, with a 95% confidence interval from -0.43 to -0.14. The interval describes a range of values compatible with the observed data and the model, under the assumptions used to calculate it. Its endpoints are both on the same side of zero, which is consistent with the reported p-value of <.001 for a comparison against no difference.

General: a confidence interval communicates uncertainty about an estimated effect. A narrower interval indicates greater precision in the estimate; a wider interval indicates more uncertainty. It does not mean that a stated proportion of individual participants’ changes fall within the interval. Nor does it capture every possible source of uncertainty, such as model misspecification, unreported analysis choices, or limitations in generalizing beyond the study population.

The unadjusted recalculation gives a difference of 0.28 for 0.75 mg relative to 1.5 mg, with an interval from 0.135 to 0.425. Its positive direction reflects the reversed comparison order. The sponsor model’s interval and the recalculated interval are not identical because the calculations differ; the sponsor estimate uses the reported mixed model, whereas the recalculation is based on summary statistics.

The registry record does not report a threshold for clinical importance, so interval placement cannot by itself settle whether the magnitude matters clinically. Precision should be considered alongside the endpoint definition, analysis population, model, and the limits of the registry information.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total participants, because this is a two-arm comparison and the stated planning assumption is equal allocation. They illustrate sample sizes under a two-sided significance level of 0.05 and a normal approximation. Each row uses the observed effect or a stated fraction of it as the target effect. The original trial’s design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect, if the assumptions hold and the true effect equals the target used in that row. The 90% power column uses a higher probability of detecting that same target effect and therefore gives a larger planning number. Smaller target effects require more participants because they are more difficult to distinguish from random variation. The estimates are planning illustrations, not observed power.

These values are not evidence that the completed trial had a particular probability of success. They are not the trial’s enrollment target, and they do not show the probability that its reported result is true. The values also depend on the calculation assumptions and the observed effect used as a reference. Planning based on an observed effect can be optimistic when that estimate is uncertain. Interpret the figures as conditional illustrations of how the required per-arm sample size changes with the target effect and desired power, not as a retrospective quality score for the study.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.280; pooled standard deviation σ = 0.839.
2. n = 2 × (1.96 + 0.842)² × 0.839² / 0.280² = 140.9, rounded up to 141 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.28                      # observed difference in means
sigma <- 0.838865786858881                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(4809220)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 141 (80% power), 189 (90% power)
 75% of observed effect: n per arm = 251 (80% power), 336 (90% power)
 50% of observed effect: n per arm = 564 (80% power), 755 (90% power)
power.t.test: 141.9 
Simulated power at n = 141 per arm: 0.801 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis used a mixed model and reported an LS mean difference of -0.29, with a 95% confidence interval from -0.43 to -0.14 and p <.001. The unadjusted recalculation from posted summary statistics gives 0.28 when the contrast is expressed as 0.75 mg minus 1.5 mg. The opposite signs reflect the different group order: the sponsor’s reported contrast is expressed in the reverse direction.

The recalculation is a simple, unadjusted comparison based on the posted group summary statistics, while the sponsor result is model-based and accounts for the listed variables and repeated-measures structure. The estimates are close in magnitude, but their intervals and exact values are not identical. The registry record does not give enough detail to attribute each difference to a particular modeling choice.

The discrepancy flag is false. The recalculation can serve as a transparent check on the approximate scale of the contrast, but it does not replace the sponsor’s analysis or reproduce the participant-level model. The sponsor’s reported analysis is the appropriate primary reference for the registry’s stated mixed-model comparison.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several endpoints, time points, or comparisons. General: as the number of statistical tests increases, the chance of at least one apparently notable result under a collection of null hypotheses can increase. Researchers can plan procedures to control a chosen error rate, or designate a primary endpoint and treat other analyses as supportive. The registry record identifies a primary endpoint and lists secondary outcomes, but any specific adjustment strategy for multiple testing is not reported in the registry record.

The primary outcome is change in HbA1c at Week 26. Secondary outcomes include HbA1c at Week 52, fasting serum glucose, self-monitored glucose, body weight, and HbA1c target attainment. The presence of several outcomes means secondary findings should be read as a set and not as isolated confirmations. The record does not report whether a hierarchy, gatekeeping process, or other multiplicity procedure was prespecified.

The primary analysis population is described as randomly assigned participants, excluding the GCP compliance investigative site, who received at least one dose and had at least one post-baseline value for the analysis. This is a specific analyzed population rather than an unrestricted all-randomized population. The registry record does not report a complete participant flow by analysis or explain the number and reasons for missing measurements.

The endpoint description names a mixed model for repeated measures, but the missing-data assumptions, any imputation method, and sensitivity analyses are not reported in the registry record. General: estimates from incomplete longitudinal data can depend on why observations are missing and on whether the model’s assumptions are reasonable. A complete evaluation of robustness would require the missing-data methods and relevant sensitivity results. The registry information does not permit those aspects to be assessed.

The original sample-size justification, planned interim analyses, and full statistical analysis plan are also not reported in the registry record. The planning illustrations based on the observed effect cannot fill in those omissions or establish what the study originally planned.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cervix carcinoma stage 0 (0.9%), angina pectoris (0.5%), retinal haemorrhage (0.5%), vitreous haemorrhage (0.5%), colitis ischaemic (0.5%).

The registry record lists serious adverse events among participants at risk: 15 of 391 in the dulaglutide 1.5 mg group and 7 of 195 in the 0.75 mg group. The record lists one death in the 1.5 mg group and none in the 0.75 mg group. These are counts within the safety information reported, not estimates of comparative risk adjusted for follow-up or participant characteristics.

Among the listed serious adverse event terms, cervix carcinoma stage 0 is reported at 0.9%; angina pectoris, retinal haemorrhage, vitreous haemorrhage, colitis ischaemic, and gastric ulcer haemorrhage are each reported at 0.5%. The registry record provides these selected terms and percentages; it does not provide enough information to determine whether events were judged related to study intervention, how long each participant was followed for safety, or how event rates compared statistically.

General: serious adverse event counts describe events meeting a seriousness definition and should not be confused with all adverse events or with proof of causation. Differences in counts alone do not establish that one dose is safer than the other. The figures should be read as a descriptive part of the registry record, not as individualized medical guidance.

17. What the Result Does, and Does Not, Mean

The primary result describes a model-estimated difference in mean HbA1c change at Week 26 between two dulaglutide-dose groups in the stated analysis population. The sponsor-reported contrast has a 95% confidence interval that does not include zero and a p-value of <.001. This is evidence of a statistical difference between group means under the reported analysis, not a statement about the response of every participant.

The result does not, by itself, establish how clinically important the estimated difference is. The registry record does not report a clinical-importance threshold for HbA1c change. It also does not establish the effect of dulaglutide compared with no dulaglutide or a different medication: the reported primary comparison is between two dulaglutide doses. Both groups received active study intervention.

The findings do not establish long-term outcomes beyond the study follow-up, nor do they automatically apply to populations other than the Japanese participants studied. The registry record does not provide sufficient detail to evaluate all aspects of missing data, multiplicity control, or the original design assumptions. Statistical significance does not resolve those limitations.

Secondary outcomes add context but do not have the same status as the designated primary outcome, especially because a multiplicity strategy is not reported. Safety counts are descriptive and cannot, on their own, establish whether events were caused by treatment or whether one dose has a different safety profile. The appropriate reading is therefore specific: the record reports a modeled group difference in the primary endpoint, accompanied by uncertainty, in this trial setting.

18. Why This Trial Matters Statistically

This trial offers a useful example of how a registry result combines design, endpoint definition, model-based estimation, and a comparison between active dose groups. Randomization and double blinding are important design features for reducing some sources of bias, while the parallel-arm structure makes the dose-group contrast the central comparison. The primary endpoint is continuous and measured over time, so the registry’s use of a repeated-measures model is relevant to how its estimate is formed.

It also illustrates why the estimate, confidence interval, and p-value should be read together. A p-value addresses evidence against a statistical null hypothesis; the interval communicates uncertainty around the estimated contrast; and neither alone determines clinical importance. The contrast’s direction depends on the order in which groups are subtracted, as illustrated by the sponsor’s negative estimate and the recalculation expressed in the reverse order.

Finally, the record shows why supporting analyses and planning calculations need careful labels. Secondary results may provide context but can be affected by multiple testing, and their multiplicity strategy is not reported. Sample-size illustrations based on observed effects can explain how planning assumptions relate to required participant numbers, but they are not the original design justification or evidence of observed power. Reading these distinctions prevents a registry result from carrying more certainty or scope than its reported methods support.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary analysis excludes the GCP compliance investigative site and requires exposure to at least one dose and at least one post-baseline observation. The registry record does not report a complete flow of randomized participants into each analysis, the number of missing measurements, or reasons for missingness. Those omissions make it difficult to assess the representativeness of the analyzed population and the potential influence of unavailable outcomes.

The record describes the primary MMRM variables but does not report the complete model specification, including further implementation details. It does not report the missing-data assumptions or sensitivity analyses. As a result, the robustness of the model-based estimate to alternative assumptions cannot be assessed from the registry information alone.

The trial compares two dulaglutide doses, not dulaglutide with an untreated or unrelated comparator. Participants could receive dulaglutide alone or alongside one oral antihyperglycemic medication, and medication history was incorporated into the primary model. The population and treatment context should therefore remain part of any interpretation; generalizability beyond Japanese participants with type 2 diabetes is not established by these results.

The registry record does not report the original sample-size justification, interim-analysis plan, or specific multiplicity procedure. The posted secondary outcomes include more than one time point and measurement, but the status of their statistical testing is not fully described. The safety information is presented as counts and selected terms without a reported comparative safety analysis or event attribution detail. These are limitations of what can be concluded from the registry record, not evidence that unreported procedures were or were not used.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Two Doses of Dulaglutide (LY2189265) in Japanese Patients With Type 2 Diabetes — NCT04809220.
• Registry record last updated 2024-05-22; status last verified 2024-04.
• Results first posted 2023-09-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed Phase 3, randomized, double-blind, parallel-arm study of dulaglutide 1.5 mg versus 0.75 mg in Japanese participants with type 2 diabetes. Total enrollment was 591. Participants received weekly subcutaneous treatment for 52 weeks, alone or with one oral antihyperglycemic medication, subject to the described medication rules.

The primary endpoint was change in HbA1c from baseline to Week 26. The reported mixed-model comparison found an LS mean difference of -0.29, with a 95% confidence interval from -0.43 to -0.14 and p <.001. Secondary outcomes and serious adverse event counts are also recorded. The original sample-size justification, multiplicity strategy, and detailed missing-data procedures are not reported in the registry record.